Lost in Math

Sabine Hossenfelder’s new book Lost in Math should be starting to appear in bookstores around now. It’s very good and you should get a copy. I hope that the book will receive a lot of attention, but suspect that much of this will focus on an oversimplified version of the book’s argument, ignoring some of the more interesting material that she has put together.

Hossenfelder’s main concern is the difficult current state of theoretical fundamental physics, sometimes referred to as a “crisis” or “nightmare scenario”. She is writing at what is likely to be a decisive moment for the subject: the negative LHC results for popular speculative models are now in. What effect will these have on those who have devoted decades to studying such models?

Back in 2006 Lee Smolin and I published books concerned about where fundamental physics was heading, and five years ago Jim Baggott’s Farewell to Reality appeared with another take on these issues. Hossenfelder’s is the first book on this topic to appear since the LHC results showing a vanilla Standard Model Higgs and no evidence of supersymmetry or other speculative BSM physics. The remarkable thing she has done is to address this in a characteristically direct manner: go talk to those responsible and ask them what they have to say for themselves.

Four of the people that Hossenfelder interviews would be on any short list of the most influential figures in theoretical particle physics, both responsible for where we are now by their past actions, and looked to by others for a vision of where the field is going next. They are Nima Arkani-Hamed, Steven Weinberg, Frank Wilczek, and Joe Polchinski.

Arkani-Hamed is introduced with:

He’s won loads of awards, including the inaugural 2012 Breakthrough Prize for “original approaches to outstanding problems in particle physics.” The problems are still outstanding. So is Nima.

and here’s an extract from the interview

“Has the LHC changed your perspective on naturalness?” I ask.

“It’s interesting–there is this popular narrative now that theorists before the LHC were totally sure that susy will show up, but now there’s a big blow. I think that the people who are professional model builders, the people I consider to be the best people in the field, they were worried already after LEP… The good people, they were not at all sure susy would show up at the LHC. And nothing has changed qualitatively since 2000. Some loopholes have been closed, but nothing has changed qualitatively…”

As with many of the interviews, Hossenfelder intersperses her own internal response to what she’s hearing:

But not one of those “best people” spoke up and called bullshit on the widely circulated story that the LHC had a good chance of seeing supersymmetry or dark matter particles.

She doesn’t mention, but surely is aware, that many prominent theorists pre-LHC had made public bets that the LHC would find SUSY, and that those wagering this way included Arkani-Hamed himself. For accounts of the 2016 Copenhagen event where the bet was paid off, see here and here. You can read there what Arkani-Hamed had to say then about losing the bet, and the quote:

“I think Winston Churchill said that in victory you should be magnanimous,” Damgaard said after Arkani-Hamed’s talk. “I know also he said that in defeat you should be defiant. And that’s certainly Nima.”

In the interview with Hossenfelder, Arkani-Hamed goes on to say:

The people who were sure it would be there are now positive it’s not there. There are people now who speak out about being depressed or worried or scared. It drives me nuts. It’s ludicrously narcissistic. Who the fuck cares about you and your little life?

There’s a lot more in the interview and you should get the book and read the whole thing. Hossenfelder does a wonderful job of portraying both Arkani-Hamed’s serious arguments and his aggressive “Damn the torpedoes” self-confident attitude. This is not someone who is going to admit that, whatever bet he lost, some failure has occurred that indicates this is a time for reflection on mistakes made and reevaluation of the path forward.

Hossenfelder travels to Austin, Texas to talk to Steven Weinberg, who it appears may not realize she is a physicist, just has been told he is supposed to talk to a “writer”. She notes that:

Weinberg doesn’t talk with you, they told me, he talks at you. Now I know what they mean. And let me tell you, he talks like a book, almost print-ready.

I won’t try and reproduce much of her conversation with Weinberg, the multiverse is a main topic (she thinks it’s an empty idea, Weinberg is willing to go along with it). About where particle theory is headed, Weinberg says:

I don’t know how much elementary particle physics can improve over what we have now. I just don’t know. I think it’s important to try and continue to do experiments, to continue to build large facilities… But where it will end up I don’t know. I hope it doesn’t just stop where it is now. Because I don’t find this entirely satisfying…

I don’t take seriously any negative conclusion that the fact that the LHC hasn’t seen anything beyond the standard model shows that there isn’t anything that will solve the naturalness problem… Supersymmetry hasn’t been ruled out because it’s too vague about what it predicts.

Her next interviewee is Frank Wilczek, who she finds in Tempe, Arizona. His take on string theory unification is rather negative:

… it’s not clear what the theory is. It’s kind of miasma of ideas that hasn’t yet taken shape, and it’s too early to say whether it’s simple or not–or even if it’s right or not. Right now it definitely doesn’t appear simple.

Asked about the argument that string theory could reproduce gravity, Wilczek responds:

If your standards are low enough, yes. But I don’t think we should compromise on this idea of post-empirical physics. I think that’s appalling, really appalling… If there was any bit of experimental evidence that was decisive and in favor of the theory, you wouldn’t be hearing these arguments. You wouldn’t. Nobody would care. It’s just a fallback. It’s giving up and declaring victory. I don’t like that at all.

Wilczek is still unwilling to give up on SUSY and the idea of a SUSY GUT, with his main argument the coupling constant unification calculation he did with Dimopoulos and Raby back in 1981:

“I am starting to get worried, yes. I never thought it would be easy. There have been bounds from [the LEP experiments] and proton decay for a long time, and this indicated that a lot of the superpartners have to be heavy. But we have another good shot with the [LHC] energy upgrade. Hope springs eternal… I would definitely not believe in supersymmetry if it wasn’t for the unification of gauge couplings, which I find very impressive. I can’t believe that’s a coincidence.”

It’s not mentioned in this book [actually, she does mention this], but Wilczek has already paid off one bet about SUSY (with Garrett Lisi) and likely will have to pay off another next year. I don’t know if by “energy upgrade” he’s thinking of the HE-LHC, or the 100 km much bigger proposed ring, but in any case those won’t happen before at least 2040. No matter what happens, I don’t think Wilczek will ever change his mind about the SUSY-GUT paradigm he has found attractive since the 1980s.

In January 2016 Hossenfelder traveled to Santa Barbara to talk to Joe Polchinski, who was already sick with the brain cancer that ultimately would take his life two years later. Unlike Wilczek, Polchinski was a fan of string theory and of evaluating it by “post-empirical” criteria. He at one point published a “Bayesian” calculation arguing that string theory is correct with probability “over 3 sigma” (i.e. over 99.7%). Asked about prospects for a unified theory, Polchinski says:

I think string theory is incomplete. It needs new ideas… But string theory has been so successful that the people who are going to make progress are the people who will be building on this idea.

Arkani-Hamed, Weinberg, Wilczek and Polchinski reflect a range of points of view about the current situation and what it means. Unfortunately it seems to me that they share an unwillingness to face up to failure, and this doesn’t bode well for the future of particle theory, with “more of the same” the agenda that is being set.

Besides these four interviews, the book also contains accounts of meeting and discussions with quite a few other physicists, all well worth reading, and often written with a sly humor. The description of visiting Garrett Lisi on Maui is not to be missed, and he has a lot of sensible things to say (“For a surf bum, he’s surprisingly intellectual” the author writes). He tells the story of how Jacques Distler and others threatened (unsuccessfully) to organize a boycott of Scientific American if it published an article by him. In addition to the interviews there’s a great deal of valuable discussion of the problems with the way research is organized and the reward structures scientists operate under (for instance, publicly admitting failure is definitely on the “not encouraged” list).

So far I’ve ignored the main framing device that Hossenfelder uses throughout the book, that of her questioning the idea of “beauty” as a motivation for evaluating ideas about physics. This is not because I disagree all that much with what she writes, but instead that I fear a complex set of issues is likely to get over-simplified, and this over-simplified version of the book’s argument is all that much of the public is ever going to hear about it. Hossenfelder explains that the concept of “beauty” she is challenging is a specific set of ideas about “symmetry, unification and naturalness” that she sees as dominating physics research. I agree that there’s a problem with this specific set of ideas and how they have been used, but I’d keep them separate and don’t see putting them together as “beauty” to be helpful. At various points she makes it clear that her worry is that we are getting stuck due to outdated notions of “beauty”, while still believing that successful new ideas will come with a new form of “beauty”.

The book ends with

We know that the laws of nature we presently have are incomplete. To complete them, we have to understand the quantum behavior of space and time, overhauling either gravity or quantum physics, or maybe both. An the answer to this will without doubt raise new questions…

…There’s much work to do. The next breakthrough in physics will occur in this century.

It will be beautiful.

Update: Science magazine has a review. For some reason they seem to have decided it was a good idea to have the book reviewed by a postdoc doing exactly the sort of work the book is most critical of. The review starts off by quoting nasty anonymous criticism of Hossenfelder from someone the reviewer knows on Facebook. Ugh.

61 Responses to Lost in Math

In a sense, the use of “theoretical physicists” in these articles is on track because in the layperson’s eye, theoretical physics IS associated with “The Quest for the Theory of Everything”. Maybe we have Stephen Hawking to thank for that.

An analogy might be how “investment bankers” have been broadly implicated in the great financial crash of 2008.
But actually the big bulk of that was specifically traders in credit derivatives of various sorts. Those doing mergers and acquisitions – which is a huge part of investment banking – were not really part of this.

And just an addendum – I also think “particle physics” is a misleading term because it makes it seem like these people are trying to find new particles.
Whereas in reality, these are all attempts to find the fundamental laws of nature.

Maybe “fundamental physics” ? Or would that raise the hackles of all the “non fundamental” physicists? 🙂

“Maybe “fundamental physics” ? Or would that raise the hackles of all the “non fundamental” physicists”

Yes, I also think “fundamental physics” is the correct term.
Also, I’m never sure why people use human-centred “high-energy physics” instead of “particle physics”, which seems the better term. You’re only calling it “high energy” because you’re low-energy – it’s not high energy to a quark.

While haggling about correct terms, let me point out that theoretical particle physics is progressing by leaps and bounds, and it’s incorporating maths in novel ways all the time. It’s just not the kind of fundamental physics that tries to find new theories that’s making these steps, it’s the kind that takes existing theories and applies them to actual experiments. Calculating differential cross-section for multi-body final states beyond leading order has become more or less routine with automated tools available, two-loop calculations are becoming more and more common, and are rapidly becoming a routine thing for two-body final states, hadronization is studied quantitatively etc.

It’s perhaps not the way we expected our knowledge would progress and not the way we expected particle physics and mathematics to cotinue their interplay, but these are significant advances.

How about “foundational physics” ? Or “foundations of physics”, the term actually used by Sabine Hossenfelder to describe her day job in a recent interview published at Edge :

” The field that I mostly work in is the foundations of physics, which is, roughly speaking, composed of cosmology, the foundations of quantum mechanics, high-energy particle physics, and quantum gravity.”

F.G.,
“Foundations” isn’t so good, since it often means work on quantum mechanics, which, whatever its problems, they’re different than the ones cause by overly speculative and experimentally inaccessible work. Chad Orzel writes about this here

I do try and properly attribute the problem to “HEP theory” or “fundamental physics”, but there is no good word that accurately picks out the part of the subject in trouble, and whatever phrase one picks, it’s likely to be too long for many headline writers.

Science magazine did it more or less the right way. They removed the quote, and then they put a note in saying they removed the note. There’s other problems with the review, but it is worth noting that many of our larger newspapers do not adhere to basic editorial standards. It’s quite common nowadays to rewrite an article with a changelog. At least someone higher up the foodchain said, hey, this is not OK and fixed it.

Perhaps the reason our theoretical pyramid is unstable is that it’s been built upside down. No amount of nth order QFT applied to ideas resting on too small a foundation will succeed – and if it does, then Nature is an ass. Mathematics contains enormously generative, and beautiful, structures that resonate perfectly with the universe we actually observe.

I look forward to reading Sabine’s book. It will eventually sit on my shelf next to Peter’s and Smolin’s books. Then I’ll go rewatch the Red Sox job offer scene in the film Moneyball, and stop thinking about things that will not change in my lifetime.